the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 02 Dec 2025
Assessing the Impacts of Land Use and Land Cover-Based Drought Adaptation Measures with an Eco-Hydrological Model
Abstract. Europe has warmed by about 1.5 °C above pre-industrial levels and endured record-breaking droughts from 2018–2020, underscoring the need for adaptation to water scarcity. This study examines the potential of targeted land use and land cover (LULC) changes to modify water fluxes and soil moisture storage for greater hydrologic drought resilience. Evaluated measures comprise replacing grain corn with sorghum on agricultural fields, converting coniferous forests (spruce, pine) to broadleaved stands (beech, oak), and mitigating imperviousness in built-up areas.
The study area, the 1,983 km² Upper Lippe catchment in Germany, and the exceptionally dry period of 2011–2020, are suitable conditions to address the research question for a temperate region. The assessment was conducted with the eco-hydrological model SWAT+ and novel approaches were implemented to accurately parameterize agricultural land use and management, dominant tree species, and the realistic impervious fraction of built-up areas within the model using publicly available existing data products and studies. After applying a calibration strategy that specifically targeted low-flow periods, the model performs well in the study period combining a good representation of low-flow periods with a standardized Root Mean Square Error for flows exceeding a 70 % probability threshold of 0.14 and while also maintaining robust overall streamflow dynamics with a modified Kling-Gupta Efficiency (KGE’) of 0.90 at the catchment outlet. The parameterization and calibration approaches can serve as references for model setups addressing similar ecoregions and research questions.
In the adapted agricultural areas, the evapotranspiration coefficient decreased by -11.7 percentage points (pp, area weighted median of the annual average) with reductions concentrated in the vegetation period leading to increases in soil moisture content. In response, the drainage flow coefficient increased by +3.3 pp with increases concentrated in the winter months and the groundwater recharge coefficient increased by +4.8 pp with a relatively uniform distribution throughout the year. The evapotranspiration coefficient from the adapted forested areas was reduced by -15.9 pp (from 67.5 %) with reductions occurring outside of the summer months. Here, increased soil moisture content increases the lateral flow coefficient by +9.0 pp and the groundwater recharge coefficient by 3.8 pp. Surface runoff increases only slightly, with enhanced surface runoff primarily occurring in mountainous areas where broadleaf trees provide less rainfall interception during winter dormancy. In the adapted built-up areas, reductions in impervious surfaces led to an increased groundwater recharge coefficient (+0.4 pp) and a decreased surface runoff coefficient (-3.6 pp), while the evapotranspiration coefficient increased (+2 pp), particularly in summer. Plant-available moisture in the topsoil increased in the adapted agricultural and forested areas across all modeled adaptation measures, reducing magnitude and duration of water stressed periods. These results demonstrate that LULC adaptations can shift landscape water balance by reducing evapotranspiration and increasing infiltration, thereby strengthening drought resilience and offering co‑benefits such as urban cooling. Such insights can guide policy and land management toward scalable, land use‑based solutions for extreme weather resilience under a warming global climate.
Competing interests: The authors declare that they have no conflict of interest. PW is a member of the editorial board of HESS.
Publisher's note: Copernicus Publications remains neutral with regard to jurisdictional claims made in the text, published maps, institutional affiliations, or any other geographical representation in this paper. While Copernicus Publications makes every effort to include appropriate place names, the final responsibility lies with the authors. Views expressed in the text are those of the authors and do not necessarily reflect the views of the publisher.- Preprint
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RC1: 'Comment on egusphere-2025-5221', Anonymous Referee #1, 17 Jan 2026
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AC2: 'Reply on RC1', Sven F. Grantz, 13 Mar 2026
Dear Referee #1,
On behalf of all authors, I would like to thank you for your comprehensive feedback on our work. Your remarks are very valuable for the publication and we are convinced that the integration of your feedback will improve the manuscript. Please find our answers concerning your major comments below and direct replies to your comments within the manuscript in the attached PDF.
With kind regards
Sven Grantz
1. The choice of the Hargreaves method. This choice in my opinion leads to a logical flaw in the paper that does not the reflect the further efforts put in by the authors. The choice of the Hargreaves methods is especially surprising as the catchment is in data-rich Germany and moreover a comprehensive meteorological dataset was used (HYRAS) that already contains all required information (except wind) to apply the Penman-Monteith method.
I personally do not see a single reason that speaks for this choice. This is indirectly confirmed by the authors as they have done a very uncommon calibration tweak which is the change of the empirical Hargreaves coefficient of 0.0023 to reduce evapotranspiration. In detail, the Harggreaves method drastically conpromises physical or more precisely plant physiological interpretability. This is in a sense completely contrasting the efforts the authors have chosen to implement small-scale crop and land use information, the comprehensive adaption of the crop/plant databse, cropping calendars and integration of novel availale datasets in the model setup. This was a missed opportunity to make the results stronger and increase the interpretability of the results. The authors should provide strong arguments about this choice, indeed using Penman in a second version would be the best solution, albeit I fear time constraints make this an impossible thing.Reply: Thank you very much for your comments and suggestions. We agree that the Penman–Monteith method represents the more physically based formulation and would, in principle, be preferable if all required meteorological inputs were available at a spatially consistent resolution. We have chosen the Hargreaves method for the following reasons:
- The Penman–Monteith method requires, among other inputs, wind data. The HYRAS climate dataset was used because of its high spatial resolution. However, it does not contain wind data and only one weather station with wind data for the whole investigation period is available in the study area. We aimed to maintain consistency in the spatial resolution of the input data and therefore preferred not to use one point measurement for wind in combination with the spatially distributed HYRAS dataset.
- We avoided PET methods requiring radiation, wind speed, and humidity because these inputs are not as readily or densely available as temperature-based inputs due to lower station density and because they are less commonly provided as outputs from climate change models. To avoid limiting the model’s flexibility when applying future climate change scenarios, and to prevent additional uncertainty in the bias-correction process arising from the lower station density of these variables, we selected the Hargreaves PET equation.To verify the evapotranspiration calculated by SWAT+ with the calibration coefficient (adjusted as described in the manuscript), we compared the results against the MODIS ET product (Running et al., 2021) and found a bias of only 12%. This indicates that the selected Hargreaves PET method provides a reasonable representation of catchment-scale evapotranspiration for the objectives of this study. However, we acknowledge that this choice limits the plant physiological interpretability relative to a Penman–Monteith-based setup, and we will make this limitation more explicit in the revised discussion.
The coefficient in the Hargreaves equation has been described by the original authors as a calibration coefficient to compensate for differences in site conditions and its value was calibrated empirically to a study area in Davis, California (Hargreaves and Samani, 1985). Coherent with this definition, the calibration coefficient is one of the default calibration parameters in the applied revision of SWAT+. Several studies report calibrating the Hargreaves equation to better represent local climate dynamics, e.g. Ferreira et al. (2024), Moratiel et al. (2020).
2. No impacts on the catchment-scale were provided. If I understood correctly all presented results refer to the land-use/ scenario specific areas (those that were changed in the scenarios. The authors even ackowledged this in the conclusion section, where they state other studies should do that. However, I appeal to the scientific ambitions of the authors that this should already have been done in their study and should be caught up on during the review. The information is already there and easy to implement. At least it must be clear in which order of magnitude the aggregated effects of the 3 scenarios are for the catchment.
Reply: Thank you for highlighting the importance of evaluating the aggregated effects of the land use modifications at the catchment scale. In the revised manuscript, we will therefore include and discuss catchment-scale aggregated water balance components in the Results and Discussion sections.
3. The authors have chosen an unconventional calibration approach of using just 1 iteration and shooting with 19,200 simulations around thre. I see multiple constraints here (see PDF comments) and I would need more information how this choice is justified. Though, the 19,200 simulations seem a bit arbitrary as well.
Reply: A reason to calibrate with several iterations is limited computing power requiring a relatively low number of simulations and thus the parameter space needs to be narrowed down. The chosen approach allowed for a high number of simulations and thus a sufficiently high resolution in the parameter space. Similar approaches have been applied successfully in several SWAT/SWAT+ modeling studies, for example by Kiesel et al. (2020), Wagner et al. (2022) or Leone et al. (2024).
We chose this number of simulations as a compromise between computational time requirements and the need for a sufficiently large ensemble to adequately cover the multi-dimensional parameter space. The exact number of 19,200 simulations was chosen because we used a high-performance computing cluster running 32 parallel processes, and this total was chosen as a multiple of 32 to fully utilize the available computational resources.
4. Another missed opportunity that contrasts the strong efforts the authors put into the model setup and especially their spatial representation of details and information, is why the additional gauges were not used for calibration and just an outlet-only approach is chosen. Although the cross validation results are decent I see some limitations here, as a better regionalization would have been possible (wrt. parameters). Please comment. I see no valid point why the 19,200 simulations could not have been performed also for the subbasins first. I guess model skill was squandered here.
Reply: Thank you very much for this important comment. We agree that spatially differentiated parameterization could, in principle, have improved the fit at individual subbasins. However, our decision not to regionalize the parameters was deliberate. Our objective was to derive a single, spatially consistent parameterization for the entire catchment. Allowing different parameter sets for different regions would have increased calibration flexibility but also the risk of compensating for structural model deficiencies through local parameter adjustment, thereby reducing parameter identifiability and increasing equifinality. In that case, improved performance at internal gauges would not necessarily indicate a more robust model but could partly reflect overfitting to the monitored subcatchments.
We specifically tested multi-gauge calibration by including the interior gauges in the objective function in addition to the outlet gauge. While this improved fit at some individual locations, it did not reduce the systematic spatial pattern of headwater discharge overestimation (PBIAS 23.5, gauge Bentfeld) and lowland underestimation (PBIAS -10.3, gauge Overhagen 2) shown in Table 4 on page 15. Therefore, we retained the calibration strategy that prioritizes integrated performance at the catchment outlet consistent with the study’s catchment-scale focus. By not using the subcatchment gauges for calibration, their validity for validation is particularly high.
We propose to include these considerations in the discussion part of the manuscript to make them more transparent to the reader.
5. The discussion sections significantly lacks a summary of potential limitations, actually the authors do barely comment on limitations at all and imply strong overstatements of the findings. This must be changed rigorously.
Reply: Thank you for this important remark. We agree that the discussion should more transparently articulate both general limitations of SWAT+ and study-specific constraints and uncertainties. While the current manuscript already includes some qualitative contextualization (e.g., linking simulated evapotranspiration responses to published experimental evidence and prior hydrologic understanding), the breadth and depth of the limitations discussion will be expanded in the revised manuscript.
6. I am missing the initial links and further information of the changes the authors did in terms f the plant database. It seems significant changes were done here and these modifications could be highly beneficial for other users as well, yet, they are neither documented nor was sufficiently explained how these changes might influence the model results given the choice Hargreaves method. This gave huge potential for the discussion section but was ignored largely.
Reply: We agree to elaborate more clearly which plant parameters were adapted and for which plants default parameters were used. The default SWAT+ plant database parameters (simplified EPIC plant growth formulation) were used for the investigated crops (corn and sorghum), while forest growth was simulated using adapted plant parameters to better represent tree growth under German conditions. The latter adaptations are based on Müller (2022) and are documented there in Table 24 of the Appendix. We also agree to elaborate further on the plant parameterizations’ relation with the model results in the discussion section.
Müller (2022) also used the Hargreaves method to determine PET, reporting superior model performance compared to the Penman-Monteith method.
7. I was also missing the link to CN2, as Hargreaves was chosen I think many water balance changes could go back to CN changes rather than plant physiological reasons (how the authors state it), however, this impact on runoff generation/infiltration is not discussed or mentioned at all. CN2 impacts should be explored further. It needs to get clearer what the main drivers of the water balance in detail are, is it more the LAI change that scales PET of Hargreaves or is it the runoff generation change? What are the contributions, I think a lot can be done here.
Reply: Thank you very much for this suggestion. We agree to include more detailed model results in the study and discuss the identified changes in the modeled water balance components of the modified areas with regard to the underlying processes.
8. Strongly connected to point 7, as the authors correctly discussed LAI impacts, I was wondering throughout the whole read why no LAI results were shown on the monthly/seasonal scale? This is a must in my opinion, especially given its later occurence in the discussion. Besides, to be less speculative, but more accurate and confident, I would recommend providing an ETA decomposition into canopy interception, transpiration and soil evaporation, to disentangle the changes in ETA for the scenarios.
Reply: Thank you very much for these suggestions to include additional model results in the research paper. We propose to include information on the LAI development of the major plants investigated in this study. Furthermore, we propose adding disaggregated actual evapotranspiration model results to Table 5 on page 19.
References
Ferreira, A., Cameira, M. d. R., and Rolim, J.: Methodology for Obtaining ETo Data for Climate Change Studies: Quality Analysis and Calibration of the Hargreaves–Samani Equation, Climate, 12, 205, doi:10.3390/cli12120205, 2024.
Hargreaves, G. H. and Samani, Z. A.: Reference Crop Evapotranspiration from Temperature, Applied Engineering in Agriculture, 1, 96–99, doi:10.13031/2013.26773, 1985.
Kiesel, J., Kakouei, K., Guse, B., Fohrer, N., and Jähnig, S. C.: When is a hydrological model sufficiently calibrated to depict flow preferences of riverine species?, Ecohydrology, 13, doi:10.1002/eco.2193, 2020.
Leone, M., Gentile, F., Lo Porto, A., Ricci, G. F., Schürz, C., Strauch, M., Volk, M., and Girolamo, A. M. de: Setting an environmental flow regime under climate change in a data-limited Mediterranean basin with temporary river, Journal of Hydrology: Regional Studies, 52, 101698, doi:10.1016/j.ejrh.2024.101698, 2024.
Moratiel, R., Bravo, R., Saa, A., Tarquis, A. M., and Almorox, J.: Estimation of evapotranspiration by the Food and Agricultural Organization of the United Nations (FAO) Penman–Monteith temperature (PMT) and Hargreaves–Samani (HS) models under temporal and spatial criteria – a case study in Duero basin (Spain), Nat. Hazards Earth Syst. Sci., 20, 859–875, doi:10.5194/nhess-20-859-2020, 2020.
Müller, E. V.: Analysis of forest-specific ecosystem services with regard to water balance components: Runoff and groundwater recharge in the forest, Landesforsten Rheinland-Pfalz, Trier, 238 pp., 2022.
Running, S., Mu, Q., Zhao, M., and Moreno, A.: MODIS/Terra Net Evapotranspiration Gap-Filled Yearly L4 Global 500m SIN Grid V061, NASA, 2021.
Wagner, P. D., Bieger, K., Arnold, J. G., and Fohrer, N.: Representation of hydrological processes in a rural lowland catchment in Northern Germany using SWAT and SWAT +, Hydrological Processes, 36, doi:10.1002/hyp.14589, 2022.
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AC2: 'Reply on RC1', Sven F. Grantz, 13 Mar 2026
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RC2: 'Comment on egusphere-2025-5221', Anonymous Referee #2, 03 Feb 2026
The manuscript ”Assessing the Impacts of Land Use and Land Cover-Based Drought Adaptation Measures with an Eco-Hydrological Model” focuses on a very current and relevant topic. It is generally well-written, even though the wording is a bit clunky here and there. For example, it is not necessary to point out repeatedly that the authors are referring to the “investigated land uses”. In my opinion, this is reasonably obvious once the scenarios have been explained. Also, the authors jump back and forth between present and past tense. The same tense should be used consistently throughout the manuscript. I made some more specific suggestions regarding the language in the attached pdf.
I have a few main concerns regarding the SWAT+ application presented in the manuscript:
- The simulated crop (at least corn and sorghum) and forest growth were not compared to observed values. To me, this is an important prerequisite for the scenario simulations run in this study. An analysis of the biomass and LAI development over the growing period/year would have been a nice way of making sure that the model is adequately calibrated for the purpose of the model application.
- Likewise, a comparison of the simulated water balance components to observed data, e.g., typical ET values from corn, sorghum, the different forest types, and urban areas (even if not from the study area), water yield estimates based on observed precipitation and streamflow from sub-catchments upstream of reservoirs/lakes, baseflow estimates using baseflow filters on observed streamflow from sub-catchments upstream of reservoirs/lakes. The authors touch on this in Lines 549-554, but I would have liked to see a more systematic assessment of the water balance components.
- Speaking of the overestimation of streamflow in the headwaters and the underestimation of streamflow in the lowland parts of the catchment: Do you think that this could have been avoided by using the additional gauges for calibration instead of validation?
- I am missing a more detailed discussion of the results in the context of similar studies (there must be published articles available on similar modelling studies). Furthermore, I would have liked to see a more honest discussion of limitations of the SWAT+ model in general and the model setup and calibration for this study.
Please see the attached pdf for additional, more specific comments.
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AC1: 'Reply on RC2', Sven F. Grantz, 13 Mar 2026
Dear Referree #2,
On behalf of all authors, I would like to thank you for your comprehensive feedback on our work. We appreciate the reviewer’s efforts in suggesting detailed improvements and will use them as a basis for further improvement of the manuscript. Please find our replies concerning your major comments below (in italics) and direct replies to your comments within the manuscript in the attached PDF.
With kind regards
Sven Grantz
1. The simulated crop (at least corn and sorghum) and forest growth were not compared to observed values. To me, this is an important prerequisite for the scenario simulations run in this study. An analysis of the biomass and LAI development over the growing period/year would have been a nice way of making sure that the model is adequately calibrated for the purpose of the model application.Reply: Thank you for this important remark. In this study, crop growth was simulated using the default SWAT+ plant database parameters (simplified EPIC plant growth formulation). For forest growth, we used plant parameters based on Müller (2022) that were adapted to better represent the tree species in Germany.
We agree in principle that comparing simulated vegetation development (e.g., LAI and biomass dynamics) against observations would further strengthen confidence in the scenario simulations. However, a calibration/validation of LAI and biomass using in-situ measurements or remotely sensed LAI products representative of the modeled area was not feasible within the scope of this large-area application and would have required substantial additional data compilation and processing. Therefore, we did not perform an explicit calibration of LAI/biomass time series.
To address this limitation transparently, we will revise the manuscript to (i) describe the plant parameterization choices and their implications more explicitly, (ii) add a dedicated limitations paragraph noting that uncertainty in vegetation growth dynamics may influence the scenario analysis and (iii) include LAI development throughout the year to allow an assessment of the plausibility of the simulated plant growth dynamics.2. Likewise, a comparison of the simulated water balance components to observed data, e.g., typical ET values from corn, sorghum, the different forest types, and urban areas (even if not from the study area), water yield estimates based on observed precipitation and streamflow from sub-catchments upstream of reservoirs/lakes, baseflow estimates using baseflow filters on observed streamflow from sub-catchments upstream of reservoirs/lakes. The authors touch on this in Lines 549-554, but I would have liked to see a more systematic assessment of the water balance components.
Reply: Thank you for this suggestion. We agree that comparing simulated water balance components with independent information is valuable for assessing overall model realism. At the same time, we would like to note that the present study is not designed as a methodological multi-objective calibration study aiming to explicitly constrain each individual water balance component with separate observational datasets. Rather, the focus is on catchment-scale hydrological performance and scenario analysis.
With respect to water yield, we consider this to be at least partly constrained already through the streamflow calibration and validation, since streamflow integrates the combined response of the relevant water balance components at the catchment scale. In addition, the model performance in subcatchments is evaluated using multi-gauge validation, which provides an independent check on the spatial realism of the simulated runoff generation and routing. We will make this point clearer in the revised manuscript.
For evapotranspiration, we agree that an additional plausibility check would strengthen the presentation. We will therefore relate the simulated ET values for the investigated land use classes to typical ranges reported in the literature for crops, forest, and urban areas, while noting that such literature values are not site-specific and thus should be interpreted as a consistency check rather than a direct validation dataset.3. Speaking of the overestimation of streamflow in the headwaters and the underestimation of streamflow in the lowland parts of the catchment: Do you think that this could have been avoided by using the additional gauges for calibration instead of validation?
Reply: We agree that spatially differentiated parameterization could, in principle, have improved the fit at individual subbasins. However, our decision not to regionalize the parameters was deliberate. Our objective was to derive a single, spatially consistent parameterization for the entire catchment. Allowing different parameter sets for different regions would have increased calibration flexibility, but also the risk of compensating for structural model deficiencies through local parameter adjustment, thereby reducing parameter identifiability and increasing equifinality. In that case, improved performance at internal gauges would not necessarily indicate a more robust model but could partly reflect overfitting to the monitored subcatchments.
We specifically tested multi-gauge calibration by including the interior gauges in the objective function in addition to the outlet gauge. While this improved fit at some individual locations, it did not reduce the systematic spatial pattern of headwater discharge overestimation (PBIAS 23.5, gauge Bentfeld) and lowland underestimation (PBIAS -10.3, gauge Overhagen 2) shown in Table 4 on page 15.
Therefore, we retained the calibration strategy that prioritizes integrated performance at the catchment outlet consistent with the study’s catchment-scale focus. By not using the subcatchment gauges for calibration, their validity for validation is particularly high.
We propose to include these considerations in the discussion part of the manuscript to make them more transparent to the reader.4. I am missing a more detailed discussion of the results in the context of similar studies (there must be published articles available on similar modelling studies). Furthermore, I would have liked to see a more honest discussion of limitations of the SWAT+ model in general and the model setup and calibration for this study.
Reply: Thank you for suggesting this valuable addition. We agree that the discussion should (i) more explicitly discuss our findings against comparable modelling studies and (ii) more transparently articulate both general limitations of SWAT+ and study-specific constraints. While the current manuscript already includes some qualitative contextualization (e.g., linking simulated evapotranspiration responses to published experimental evidence and prior hydrologic understanding), the breadth and depth of the discussion of limitations will be expanded in the revised manuscript.
References
Müller, E. V.: Analysis of forest-specific ecosystem services with regard to water balance components: Runoff and groundwater recharge in the forest, Landesforsten Rheinland-Pfalz, Trier, 238 pp., 2022.
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The authors investigated how different targeted LULC change strategies could enhace drought resilience due to improved soild moisture retention and reduced evaporation losses. The investigation spanned agricultural fields, desealing and forest changes in a German test catchment. Investigations focused on a dry period (2011 and 2020) and used the widely used SWAT+ model. While the study provides valuable insights and is well written, I have several limitations that should be addressed and that need major revisions. Please note that detailled comments are in the attached PDF. Generally the paper is already well written but could benefit from some methodological clarity here and there to make i t even easier for the reader.
My main concerns are:
1. The choice of the Hargreaves method. This choice in my opinion leads to a logical flaw in the paper that does not the reflect the further efforts put in by the authors. The choice of the Hargreaves methods is especially surprising as the catchment is in data-rich Germany and moreover a comprehensive meteorological dataset was used (HYRAS) that already contains all required information (except wind) to apply the Penman-Monteith method.
I personally do not see a single reason that speaks for this choice. This is indirectly confirmed by the authors as they have done a very uncommon calibration tweak which is the change of the empirical Hargreaves coefficient of 0.0023 to reduce evapotranspiration. In detail, the Harggreaves method drastically conpromises physical or more precisely plant physiological interpretability. This is in a sense completely contrasting the efforts the authors have chosen to implement small-scale crop and land use information, the comprehensive adaption of the crop/plant databse, cropping calendars and integration of novel availale datasets in the model setup. This was a missed opportunity to make the results stronger and increase the interpretability of the results. The authors should provide strong arguments about this choice, indeed using Penman in a second version would be the best solution, albeit I fear time constraints make this an impossible thing.
2. No impacts on the catchment-scale were provided. If I understood correctly all presented results refer to the land-use/ scenario specific areas (those that were changed in the scenarios. The authors even ackowledged this in the conclusion section, where they state other studies should do that. However, I appeal to the scientific ambitions of the authors that this should already have been done in their study and should be caught up on during the review. The information is already there and easy to implement. At least it must be clear in which order of magnitude the aggregated effects of the 3 scenarios are for the catchment.
3. The authors have chosen an unconventional calibration approach of using just 1 iteration and shooting with 19,200 simulations around thre. I see multiple constraints here (see PDF comments) and I would need more information how this choice is justified. Though, the 19,200 simulations seem a bit arbitrarya s well.
4. Another missed opportunity that contrasts the strong efforts the authors put into the model setup and especially their spatial representation of details and information, is why the additional gauges were not used for calibration and just an outlet-only approach is chosen. Although the cross validation results are decent I see some limitations here, as a better regionalization would have been possible (wrt. parameters). Please comment. I see no valid point why the 19,200 simulations could not have been performed also for the subbasins first. I guess model skill was squandered here.
5. The discussion sections significantly lacks a summary of potential limitations, actually the authors do barely comment on limitations at all and imply strong overstatements of the findings. This must be changed rigorously.
6. I am missing the initial links and further information of the changes the authors did in terms f the plant database. It seems significant changes were done here and these modifications could be highly beneficial for other users as well, yet, they are neither documented nor was sufficiently explained how these changes might influence the model results given the choice Hargreaves method. This gave huge potential for the discussion section but was ignored largely.
7. I was also missing the link to CN2, as Hargreaves was chosen I think many water balance changes could go back to CN changes rather than plant physiological reasons (how the authors state it), however, this impact on runoff generation/infiltration is not discussed or mentioned at all. CN2 impacts should be explored further. It needs to get clearer what the main drivers of the water balance in detail are, is it more the LAI change that scales PET of Hargreaves or is it the runoff generation change? What are the contributions, I think a lot can be done here.
8. Strongly connected to point 7, as the authors correctly discussed LAI impacts, I was wondering throughout the whole read why no LAI results were shown on the monthly/seasonal scale? This is a must in my opinion, especially given its later occurence in the discussion. Besides, to be less speculative, but more accurate and confident, I would recommend providing an ETA decomposition into canopy interception, transpiration and soil evaporation, to disentangle the changes in ETA for the scenarios.